Nick Brown's blog

13 March 2018

(Update 2018-03-14 10:18 UTC: I have received lots of offers to help with this, and I now have enough people helping. So please don't send me an e-mail about this.)

Back in the spring of 2016, for reasons that
don’t matter here, I found myself needing to understand a little bit about the
NHANES (National Health and Nutrition
Examination Survey) family of datasets.
NHANES is an ongoing programme that has been running in the United
States since the 1970s, looking at how nutrition and health interact.

Most of the datasets produced by the various waves of NHANES are available to
anyone who wants to download them. Before I got started on my project (which,
in the end, was abandoned, again for reasons that don’t matter here), I thought that it was a good idea to check that I understood the structure of the data by reproducing the
results of an article based on them. This seemed especially important because the
NHANES files—at least, the ones I was interested in—are supplied in a format that requires SAS to read,
and I needed to convert them to CSV before analyzing them in R.So I thought the best way to check this would
be to take a well-cited article and reproduce its table of results, which would allow me to be reasonably confident that I had done the conversion right, understood the variable
names, etc.

Since I was using the NHANES-IIIdata (from the third wave of the NHANES programme, conducted in the mid-1990s) I chose an
article at random by looking for references to NHANES-III in Google Scholar
(I don’t remember the exact search string) and picking the first article that had several hundred citations. I won't mention its title here (read on for more details), but it addresses what is clearly an important topic and seemed like a very nice paper—exactly what I was looking for to test whether or not I was converting, importing, and interpreting the NHANES data correctly.

The NHANES-III datasets are distributed in good old-fashioned mainframe magnetic tape format, with every field having a fixed width. There is some accompanying code to interpret these files (splitting up the tape records and adding variable names) in SAS. Since I was going to do my analyses in R, I needed to run this code and export the data in CSV format. I didn't have access to SAS (in fact, I had never previously used it), and it seemed like a big favour to ask someone to convert over 280 megabytes of data (which is the size of the three files that I downloaded) for me, especially because I thought (correctly) that it might take a couple of iterations to get the right set of files. Fortunately, I discovered the remarkable SAS University Edition, which is a free-to-use version of SAS that seems to have most of the features one might want from a statistics package. This, too, is a big download (around 2GB, plus another 100MB for the Oracle Virtual Machine Manager that you also need—SAS are not going to allow you to run your software on any operating system, it has to be Red Hat Linux, and even if you already have Red Hat Linux, you have to run their virtualised version on top!), but amazingly, it all worked first time. As long as you have a recent computer (64-bit processor, 4GB of RAM, a few GB free on the disk) this should work on Windows, Mac, or Linux.

Having identified and downloaded the NHANES files that I needed, opening those files using SAS University Edition and exporting them to CSV format turned out to required just a couple of lines of code using PROC EXPORT, for which I was able to find the syntax on the web quite easily. Once I had those CSV files, I could write my code to read them in, extract the appropriate variables, and repeat most of the analyses in the article that I had chosen.

Regular readers of this blog may be able to guess what happened next: I didn’t get the same results as the
authors.I won’t disclose too many details here
because I don’t want to bias the reanalysis exercise that I’m proposing to
conduct, but I will say that the differences did not seem to me to be trivial. If my numbers are correct then a fairly substantial correction to the tables of results will be required. At least one (I don't want to give more away) of the statistically significant results is no longer statistically significant, and many of the significant odds ratios are considerably smaller. (There are also a couple of reporting errors in plain sight in the article itself.)

When I discovered these apparent issues back in 2016, I wrote to the lead author, who told me that s/he was rather busy and invited me to get in touch again after the summer. I did so, but s/he then didn't reply further. Oh well. People are indeed often very busy, and I can see how, just because one person who maybe doesn't understand everything that you did in your study writes to you, that perhaps isn't a reason to drop everything and start going through some calculations you ran more than a decade ago. I let the matter drop at the time because I had other stuff to do, but a few weeks ago it stuck its nose up through the pile of assorted back burner projects (we all have one) and came to my attention again.

So, here's the project. I want to recruit a few (ideally around three) people to independently reanalyse this article using the NHANES-III datasets and see if they come up with the same results as the original authors, or the same as me, or some different set of results altogether. My idea is that, if several people working completely independently (within reason) come up with numbers that are (a) the same as each other and (b) different from the ones in the article, we will be well placed to submit a commentary article for publication in the journal (which has an impact factor over 5), suggesting that a correction might be in order. On the other hand, if it turns out that my analyses were wrong, and the article is correct, then I can send the lead author a note to apologise for the (brief) waste of his time that my 2016 correspondence with him represented. Whatever the outcome, I hope that we will all learn something.

For the moment I'm not going to name the article here, because I don't want to have too many people running around reanalysing it outside of this "crowdsourced" project. Of course, if you sign up to take part, I will tell you what the article is, and then I can't stop you shouting its DOI from the rooftops, but I'd prefer to keep this low-key for now.

If you would like to take part, please read the conditions below.

1. If the line below says "Still accepting offers", proceed. If it says "I have enough people who have offered to help", stop here, and thanks for reading this far.

========== I have enough people who have offered to help ==========

2. You will need a computer that either already has SAS on it, or on which you can install SAS (e.g., University Edition). This is so that you can download and convert the NHANES data files yourself. I'm not going to supply these, for several reasons: (a) I don't have the right to redistribute them, (b) I might conceivably have messed something up when converting them to CSV format, and (c) I might not even have the right files (although my sample sizes match the ones in the article pretty closely). If you are thinking of volunteering, and you don't have SAS on your computer, please download SAS University Edition and make sure that you can get it to work. (An alternative, if you are an adventurous programmer, is to download the data and SAS files, and use the latter as a recipe for splitting the data and adding variable names.)

3. You need to be reasonably competent at performing logistic regressions in SAS, or in a software package than can read SAS or CSV files. I used R; the original authors used proprietary software (not SAS). It would be great if all of the people who volunteered used different packages, but I'm not going to turn down anyone just because someone else wants to use the same analysis software. However, I'm also not going to give you a tutorial on how to run a logistic regression (not least because I am not remotely an expert on this myself).

4. Volunteers will be anonymous until I have all the results (to avoid, as far as possible, people collaborating with each other). However, by participating, you accept that once the results are in, your name and your principal results may be published in a follow-up blog post. You also accept, in principle, to be a co-author on any letter to the editor that might result from this exercise. (This point isn't a commitment to be signed in blood at this stage, but I don't want anyone to be surprised or offended when I ask if I can publish their results or use them to support a letter.)

5. If you want to work in a team on this with some colleagues, please feel free to do so, but I will only put one person's name forward per reanalysis on the hypothetical letter to the editor; others who helped may get an acknowledgement, if the journal allows. Basically, ensure that you can say "Yes, I did most of the work on this reanalysis, I meet the criteria for co-authorship".

6. The basic idea is for you to work on your own and solve your own problems, including understanding what the original authors did. The article is reasonably transparent about this, but it's not perfect and there are some ambiguities. I would have liked to have the lead author explain some of this, but as mentioned above, s/he appears to be too busy. If you hit problems then I can give you a minimum amount of help based on my insights, but of course the more I do that, the more we risk not being independent of each other. (That said, I could do with some help in understanding what the authors did at one particular point...)

7. You need to be able to get your reanalysis done by June 30, 2018. This deadline may be moved (by me) if I have trouble recruiting people, but I don't want to repeat a recent experience where a couple of the people who had offered to help me on a project stopped responding to their e-mails for several months, leaving me to decide whether or not to drop them. I expect that the reanalysis will take between 10 and 30 hours of your time, depending on your level of comfort with computers and regression analyses.

Are you still here? Then I would be very happy if you would decide whether you think this reanalysis is within your capabilities, and then make a small personal commitment to follow through with it. If you can do that, please send me an e-mail (nicholasjlbrown, gmail) and I will give you the information you need to get started.

It was a bit more than a year ago when Dr. Brian Wansink wrote a blog post (since deleted, hence the archived copy) that attracted some negative attention, partly because of what some people saw as poor treatment of graduate students, but more (in terms of the weight of comments, anyway) because it described what appeared to be some fairly terrible ways of doing research (sample: 'Every day she came back with puzzling new results, and every day we would scratch our heads, ask "Why," and come up with another way to reanalyze the data with yet another set of plausible hypotheses'). It seemed pretty clear that researcher degrees of freedom were a big part of the business model of this lab. Dr. Wansink claimed not to have heard of p-hacking before the comments started appearing on his blog post; I have no trouble believing this, because news travels slowly outside the bubble of Open Science Twitter. (Some advocates of better scientific practices in psychology have recently claimed that major improvements are now underway. All I can say is, they can't be reviewing the same manuscripts that I'm reviewing.)

Amidst all that weirdness, it was possible to lose sight of the fact that what got everything started was the attention drawn to the lab by that initial blog post from November 2016, at which point most of us thought that the worst we were dealing with was rampant p-hacking. Since then, various people have offered opinions on what might be going on in the lab; one of the most popular explanations has been, if I can paraphrase, "total cluelessness". On this account, the head of the lab is so busy (perhaps at least partly due to his busy schedule of media appearances, testifying before Congress, and corporate consulting*), the management of the place so overwhelmed on a day-to-day basis, that nobody knows what is being submitted to journals, which table to include in which manuscript, which folder on the shared drive contains the datasets. You could almost feel sorry for them.

Stephanie's latest article changes that, at least for me. The e-mail exchanges that she cites and discusses seem to show deliberate and considered discussion about what to include and what to leave out, why it's important to "tweek" [sic] results to get a p value down to .05, which sets of variables to combine in search of moderators, and which types of message will appeal to the editors (and readers) of various journals. Far from being chaotic, it all seems to be rather well planned to me; in fact, it gives just the impression Dr. Wansink presumably wanted to give in his blog post that led us down this rabbit hole in the first place. When Brian Nosek, one of the most diplomatic people in science, is prepared to say that something looks like research misconduct, it's hard to imply that you're just in an argument with over-critical data thugs.

It's been just over eight hours since the BuzzFeed article appeared, on a Sunday evening in North America. (This post was half-drafted, since I had an idea of what would Stephanie was going to write about in her piece, having been interviewed for it. I was just about to go to sleep when my phone buzzed to let me know that the article had gone live. I will try to forgive my fellow data thug for scooping me to get the first blog about it online.) The initial social media response has been almost uniformly one of anger. If there is a split—and it would seem to be mostly implicit for the moment—it's between those who think that the Cornell Food and Brand Lab is somehow exceptional, and those who think that it's just a particularly egregious example of what goes on all the time in many psychology labs. If you're reading this on the first day I posted it, you might still be able to cast your vote about this. Sanjay Srivastava, who made that poll, also blogged a while back about a 2016 article by anthropologist David Peterson that described rather similar practices in three (unnamed) developmental psychology labs. The Peterson article is well worth reading; I suspected at the time, and I suspect even more strongly today, that what he describes goes on in a lot of places, although maybe the PIs in charge are smart enough not to put their p-hacking directives in e-mails (or, perhaps, all of the researchers involved work at places whose e-mails can't be demanded under FoI, which doesn't extend to private universities; as far as I know, Stephanie Lee obtained all of her information from places other than Cornell).

Maybe this anger can be turned into something good. Perhaps we will see a social media-based movement, inspired by some of the events of the past year, for people to reveal some of the bad methodological stuff their PIs expect them to do. I won't go into any details here, partly because the other causes I'm thinking about are arguably more important than social science research and I don't want to appear to be hitching a ride on their bandwagon by proposing hashtags (although I wonder how many people who thought that they would lose weight by decanting their breakfast cereal into small bags are about to receive a diagnosis of type II diabetes mellitus that could have been prevented if they had actually changed their dietary habits), and partly because as someone who doesn't work in a lab, it's a lot easier for me to talk about this stuff than it is for people with insecure employment that depends on keeping a p-hacking boss happy.

Back to Cornell: we've come full circle. But maybe we're just starting on the second lap. Because, as I noted earlier, all the p-hacking, HARKing, and other stuff that renders p values meaningless still can't explain the impossible numbers, duplicated tables, and other stuff that makes this story rather different from what, I suspect, might—apart, perhaps, from the scale at which these QRPs are being applied—be "business as usual" in a lot of places. Why go to all the trouble of combining variables until a significant moderator shows up in SPSS or Stata, and then report means and test statistic that can't possibly have been output by those programs? That part still makes no sense to me. Nor does Dr. Wansink's claim that he and all his colleagues "didn't remember" when he wrote the correction to the "Elmo" article in the summer of 2017 that the study was conducted on daycare kids, when in February of that year he referred to daycare explicitly (and there are several other clues, some of which I've documented over the past year in assorted posts). And people with better memories than me have noted that the "complete" releases of data that we've been given appear not to be as complete as they might be. We are still owed another round of explanations, and I hope that, among what will probably be a wave of demands for more improvements in research practices, we can still find time to get to the bottom of what exactly happened here, because I don't think that an explanation based entirely on "traditional" QRPs is going to cover it.

* That link is to a Google cache from 2018-02-19, because for some reason, the web page for McDonald's Global Advisory Council gives a 404 error as I'm writing this. I have no idea whether that has anything to do with current developments, or if it's just a coincidence.

"Extremely odd that it isn't a retraction"? Let's take a closer look.Here is the article that was corrected:Wansink, B., Just, D. R., Payne, C. R., & Klinger, M. Z. (2012). Attractive names sustain increased vegetable intake in schools. Preventive Medicine, 55, 330–332. http://dx.doi.org/10.1016/j.ypmed.2012.07.012This is the second article from this lab in which data were reported as having been collected from elementary school children aged 8–11, but it turned out that they were in fact collected from children aged 3–5 in daycares. You can read the lab's explanation for this error at the link to the correction above (there's no paywall at present), and decide how convincing you find it.Just as a reminder, the first article, published in JAMA Pediatrics, was initially corrected (via JAMA's "Retract and replace" mechanism) in September 2017. Then, after it emerged that the children were in fact in daycare, and that there were a number of other problems in the dataset that I blogged about, the article was definitively retracted in October 2017.I'm going to concentrate on Study 1 of the recently-corrected article here, because the corrected errors in this study are more egregious than those in Study 2, and also because there are still some very substantial problems remaining. If you have access to SPSS, I also encourage you to download the dataset for Study 1, along with the replication syntax and annotated output file, from here.By the way, in what follows, you will see a lot of discussion about the amount of "carrots" eaten. There has been somediscussionabout this, because the original article just discussed "carrots" with no qualification. The corrected article tells us that the carrots were "matchstick carrots", which are about 1/4 the size of a baby carrot. Presumably there is a U.S. Standard Baby Carrot kept in a science museum somewhere for calibration purposes.So, what are the differences between the original article and the correction? Well, there are quite a few. For one thing, the numbers in Table 1 now finally make sense, in that the number of carrots considered to have been "eaten" is now equal to the number of carrots "taken" (i.e., served to the children) minus the number of carrots "uneaten" (i.e., counted when their plates came back after lunch). In the original article, these numbers did not add up; that is, "taken" minus "uneaten" did not equal "eaten". This is important because, when asked by Alison McCook of Retraction Watch why this was the case, Dr. Brian Wansink (the head of the Cornell Food and Brand Lab) implied that it must have been due to some carrots being lost (e.g., dropped on the floor, or thrown in food fights). But this makes no sense for two reasons. First, in the original article, the difference between the number of carrots "eaten" was larger than the difference between "taken" and "uneaten", which would imply that, rather than being dropped on the floor or thrown, some extra carrots had appeared from somewhere. Second, and more fundamentally, the definition of the number of carrots eaten is (the number taken) minus (the number left uneaten). Whether the kids ate, threw, dropped, or made sculptures out of the carrots doesn't matter; any that didn't come back were classed as "eaten". There was no monitoring of each child's oesophagus to count the carrots slipping down.

When we look in the dataset, we can see that there are separate variables for "taken" (e.g., "@1CarTaken" for Monday, "@2CarTaken" for Tuesday, etc), "uneaten" (e.g., "@1CarEnd", where "End" presumably corresponds to "left at the end"), and "eaten" (e.g., "@1CarEaten"). In almost all cases, the formula ("eaten" equals "taken" minus "uneaten") holds, except for a few missing values and two participants (#42 and #152) whose numbers for Monday seem to have been entered in the wrong order; for both of these participants, "eaten" equals "taken" plus "uneaten". That's slightly concerning because it suggests that, instead of just entering "taken" and "uneaten" (the quantities that were capable of being measured) and letting their computer calculate "eaten", the researchers calculated "eaten" by hand and typed in all three numbers, doing so in the wrong order for these two participants in the process.

Another major change is that whereas in the original article the study was run on three days, in the correction there are reports of data from four days. In the original, Monday was a control day, the between-subject manipulation of the carrot labels was done on Tuesday, and Thursday was a second control day, to see if the effect persisted. In the correction, Thursday is now a second experimental day, with a different experiment that carries over to Friday. Instead of measuring how many carrots were eaten on Thursday, between two labelling conditions ("X-ray Vision Carrots" and "Food of the Day"; there was no "no-label" condition), the dependent variable was the number of carrots eaten on the next day (Friday).

OK, so those are the differences between the two articles. But arguably the most interesting discoveries are in the dataset, so let's look at that next.

Randomisation #fail

As Tim van der Zee noted in the Twitter thread that I linked to at the top of this post, the number of participants in Study 1 in the corrected article has mysteriously increased since the original publication. Specifically, the number of children in the "Food of the Day" condition has gone from 38 to 48, an increase of 10, and the number of children in the "no label" condition has gone from 45 to 64, an increase of 19. You might already be thinking that a randomisation process that leads to only 22.2% (32 of 144) participants being in the experimental condition might not be an especially felicitous one, but as we will see shortly, that is by no means the largest problem here. (The original article does not actually discuss randomisation, and the corrected version only mentions it in the context of the choice of two labels in the part of the experiment that was conducted on the Thursday, but I think it's reasonable to assume that children were meant to be randomised to one of the carrot labelling conditions on the Tuesday.)

The participants were split across seven daycare centres and/or school facilities (I'll just go with the authors' term "schools" from now on). Here is the split of children per condition and per school:

Oh dear. It looks like the randomisation didn't so much fail here, as not take place at all, in almost all of the schools.

Only two schools (#1 and #4) had a non-zero number of children in each of the three conditions. Three schools had zero children in the experimental condition. Schools #3, #5, #6, and #7 only had children in one of the three conditions. The justification for the authors' model in the corrected version of the article ("a Generalized Estimated Equation model using a negative binominal distribution and log link method with the location variable as a repeated factor"), versus the simple ANOVA that they performed in the original, was to be able to take into account the possible effect of the school. But I'm not sure that any amount of correction for the effect of the school is going to help you when the data are as unbalanced as this. It seems quite likely that the teachers or researchers in most of the schools were not following the protocol very carefully.

At school #1, thou shalt eat carrots

Something very strange must have been happening in school #1. Here is the table of the numbers of children taking each number of carrots in schools #2-#7 combined:

I think that's pretty much what one might expect. About a quarter of the kids took no carrots at all, most of the rest took a few, and there were a couple of major carrot fans. Now let's look at the distribution from school #1:

Whoa, that's very different. No child in school #1 had a lunch plate with zero carrots. In fact, all of the children took a minimum of 10 carrots, which is more than 44 (41.1%) of the 107 children in the other schools took. Even more curiously, almost all of the children in school #1 apparently took an exact multiple of 10 carrots - either 10 or 20. And if we break these numbers down by condition, it gets even stranger:

So 17 out of 21 children in the control condition ("no label", which in the case of daycare children who are not expected to be able to read labels anyway presumably means "no teacher describing the carrots") in school #1 chose exactly 10 carrots. Meanwhile, every single child—12 out of 12—in the "Food of the Day" condition selected exactly 20 carrots.

I don't think it's necessary to run any statistical tests here to see that there is no way that this happened by chance. Maybe the teachers were trying extra hard to help the researchers get the numbers they wanted by encouraging the children to take more carrots than they otherwise would (remember, from schools #2-#7, we could expect a quarter of the kids to take zero carrots). But then, did they count out these matchstick carrots individually, 1, 2, 3, up to 10 or 20? Or did they serve one or two spoonfuls and think, screw it, I can't be bothered to count them, let's call it 10 per spoon? Participants #59 (10 carrots), #64 (10), #70 (22), and #71 (10) have the comment "pre-served" recorded in their data for this day; does this mean that for these children (and perhaps others with no comment recorded), the teachers chose how many carrots to give them, thus making a mockery of the idea that the experiment was trying to determine how the labelling would affect the kids' choices? (I presume it's just a coincidence that the number of kids with 20 carrots in the "Food of the Day" condition, and the number with 10 carrots in the "no label" condition, are very similar to the number of extra kids in these respective conditions between the original and corrected versions of the article.)

The tomatoes... and the USDA project report

Another interesting thing to emerge from an examination of the dataset is that not one but two foods, with and without "cool names", were tested during the study. As well as "X-ray Vision Carrots", children were also offered tomatoes. On at least one day, these were described as "Tomato Blasts". The dataset contains variables for each day recording what appears to be the order in which each child was served with the tomatoes or carrots. Yet, there are no variables recording how many tomatoes each child took, ate, or left uneaten on each day. This is interesting, because we know that these quantities were measured. How? Because it's described in this project report by the Cornell Food and Brand Lab on the USDA website:

"... once exposed to the x-ray vision carrots kids ate more of the carrots even when labeled food of the day. No such strong relationship was observed for tomatoes, which could mean that the label used (tomato blasts) might not be particularly meaningful for children in this age group."

This appears to mean that the authors tested two dependent variables, but only reported the one that gave a statistically significant result. Does that sound like readers of the Preventive Medicine article (either the original or the corrected version) are being provided with an accurate representation of the research record? What other variables might have been removed from the dataset?

It's also worth noting that the USDA project report that I linked to above states explicitly that both the carrots-and-tomatoes study and the "Elmo"/stickers-on-apples study (later retracted by JAMA Pediatrics) were conducted in daycare facilities, with children aged 3–5. It appears that the Food and Brand Lab probably sent that report to the USDA in 2009. So how was it that by March 2012—the date on this draft version of the original "carrots" article—everybody involved in writing "Attractive Names Sustain Increased Vegetable Intake in Schools" had apparently forgotten about it, and was happy to report that the participants were elementary school students? And yet, when Dr. Wansink cited the JAMA Pediatrics article in 2013 and 2015, he referred to the participants as "daycare kids" and "daycare children", respectively; so his incorrect citation of his own work actually turns out to have been a correct statement of what had happened. And in the original version of that same "Elmo" article, published in 2012, the authors referred to the children—who were meant to be aged 8–11—as "preliterate". So even if everyone had forgotten about the ages of the participants at a conscious level, this knowledge seems to have been floating around subliminally. This sounds like a very interesting case study for psychologists.

Another interesting thing about the March 2012 draft that I mentioned in the previous paragraph is that it describes data being collected on four days (i.e., the same number of days as the corrected article), rather than the three days that were mentioned in the original published version of the article, which was published just four months after the date of the draft:

Extract from the March 2012 draft manuscript, showing the description of the data collection period, with the PDF header information (from File/Properties) superposed.

So apparently at some point between drafting the original article and submitting it, one of the days was dropped, with the second control day being moved up from Friday to Thursday. Again, some people might feel that at least one version of this article might not be an accurate representation of the research record.

Miscellaneous stuff

Some other minor peculiarites in the dataset, for completeness:

- On Tuesday—the day of the experiment, after a "control" day—participants 194, 198, and 206 was recorded as commenting about "cool carrots"; it is unclear whether this was a reference to the name that was given to the carrots on Monday or Tuesday. But on Monday, a "control" day, the carrots should presumably have had no name, and on Tuesday they should have been described as "X-ray Vision Carrots".

- On Monday and Friday, all of the carrots should have been served with no label. But the dataset records that five participants (#199, #200, #203, #205, and #208) were in the "X-ray Vision Carrots" condition on Monday, and one participant (#12) was in the "Food of the Day" condition on Friday. Similarly, on Thursday, according to the correction, all of the carrots were labelled as "Food of the Day" or "X-ray Vision Carrots". But two of the cases (participants #6 and #70) have the value that corresponds to "no label" here.

These are, again, minor issues, but they shouldn't be happening. In fact there shouldn't even be a variable in the dataset for the labelling condition on Monday and Friday, because those were control-only days.

Conclusion

What can we take away from this story? Well, the correction at least makes one thing clear: absolutely nothing about the report of Study 1 in the original published article makes any sense. If the correction is indeed correct, the original article got almost everything wrong: the ages and school status of the participants, the number of days on which the study was run, the number of participants, and the number of outcome measures. We have an explanation of sorts for the first of these problems, but not the others. I find it very hard to imagine how the authors managed to get so much about Study 1 wrong the first time they wrote it up. The data for the four days and the different conditions are all clearly present in the dataset. Getting the number of days wrong, and incorrectly describing the nature of the experiment that was run on Thursday, is not something that can be explained by a simple typo when copying the numbers from SPSS into a Word document (especially since, as I noted above, the draft version of the original article mentions four days of data collection).

In summary: I don't know what happened here, and I guess we may never know. What I am certain of is that the data in Study 1 of this article, corrected or not, cannot be the basis of any sort of scientific conclusion about whether changing the labels on vegetables makes children want to eat more of them.

I haven't addressed the corrections to Study 2 in the same article, although these would be fairly substantial on their own if they weren't overshadowed by the ongoing dumpster fire of Study 1. It does seem, however, that the spin that is now being put on the story is that Study 1 was a nice but perhaps "slightly flawed" proof-of-concept, but that there is really nothing to see there and we should all look at Study 2 instead. I'm afraid that I find this very unconvincing. If the authors have real confidence in their results, I think they should retract the article and resubmit Study 2 for review on its own. It would be sad for Matthew Z. Klinger, the then high-school student who apparently did a lot of the grunt work for Study 2, to lose a publication like this, but if he is interested in pursuing an academic career, I think it would be a lot better for him to not to have his name on the corrected article in its present form.

08 January 2018

A while back, someone asked me how we (Tim van der Zee, Jordan Anaya, and I) checked the validity of the F statistics when we analyzed the "pizza papers" from the Cornell Food and Brand Lab. I had an idea to write this up here, which has now floated to the top of the pile because I need to cite it in a forthcoming presentation. :-)

A quick note before we start: this technique applies to one- or two-way between-subjects ANOVAs. A one-way, two-condition ANOVA is equivalent to an independent samples t test; the F statistic is the square of the t statistic. I will sometimes mention only F statistics, but everything here applies to independent samples t tests too. On the other hand, you can't use this technique to check mixed (between/within) ANOVAs, or paired-sample t tests, as those require knowledge of every value in the dataset.

It turns out that, subject to certain limitations later), you can derive the F statistic for a between-subjects ANOVA from (only) the per-cell means, SDs, and sample sizes. You don't need the full dataset. There are some online calculators that perform these tests; however, they typically assume that the input means and SDs are exact, which is unrealistic. I can illustrate this point with the t test (!) calculator from GraphPad. Open that up and put these numbers in:

(Note that we are not using Welch's t test here, although Daniël Lakens will tell you --- and he is very probably right --- that we should usually do so; indeed, we should use Welch's ANOVA too. Our main reason for not doing that here is that the statistics you are checking will usually not have been made with the Welch versions of these tests; indeed, the code that I present below depends on an R package assumes that the non-Welch tests are used. You can usually detect if Welch's tests have been used, as the [denominator] degrees of freedom will not be integers.)

Having entered those numbers, click on "Calculate now" (I'm not sure why the "Clear the form" button is so large or prominent!) and you should get these results: t = 4.3816, df = 98. Now, suppose the article you are reading states that "People in condition B (M=5.06, SD=1.18, N=52) outperformed those in condition A (M=4.05, SD=1.12, N=48), t(98)=4.33". Should you reach for your green ballpoint pen and start writing a letter to the editor about the difference in the t value? Probably not. The thing is, the reported means (4.05, 5.06) and SDs (1.12, 1.18) will have been rounded after being used to calculate the test statistic. The mean of 4.05 could have been anywhere from 4.045 to 4.055 (rounding rules are complex, but whether this is 4.0499999 or 4.0500000 doesn't matter too much), the SD of 1.12 could have been in the range 1.115 to 1.125, etc. This can make quite a difference. How much? Well, we can generate the maximum t statistic by making the difference between the means as large as possible, and both of the SDs as small as possible:

That gives a t statistic of 4.4443. To get the smallest possible t value, we make the difference between the means as small as possible, and both of the SDs as large as possible, in an analogous way. I'll leave the filling in of the form as an exercise for you, but the result is 4.3195.

So we now know that when we see a statement such as "People in condition B (M=5.06, SD=1.18, N=52) outperformed those in condition A (M=4.05, SD=1.12, N=48), t(98)=<value>", any t value from 4.32 through 4.44 is plausible; values outside that range are, in principle, not possible. If you see multiple such values in an article, or even just one or two with a big discrepancy, it can be worth investigating further.

The online calculators I have seen that claim to do these tests have a few other limitations as well as the problem of rounded input values. First, the interface is a bit clunky (typically involving typing numbers into a web form, which you have to do again tomorrow if you want to re-run the analyses). Second, some of them use Java, and that may not work with your browser. What we needed, at least for the "Statistical Heartburn" analyses, was some code. I wrote mine in R and Jordan independently wrote a version in Python; we compared our results at each step of the way, so we were fairly confident that we had the right answers (or, of course, we could have both made the same mistakes).

My solution uses an existing R library called rpsychi, which does the basic calculations of the test statistics. I wrote a wrapper function called f_range(), which does the work of calculating the upper and lower bounds of the means and SDs, and outputs the minimum and maximum F (or t, if you set the parameter show.t to TRUE) statistics.

Usage is intended to be relatively straightforward. The main parameters of f_range() are vectors or matrices of the per-cell means (m), SDs (s), and sample sizes (n). You can add show.t=TRUE to get t (rather than F) statistics, if appropriate; setting dp.p forces the number of decimal places used to that value (although the default almost always works); and title and labels are cosmetic. Here are a couple of examples from the "pizza papers":

I mentioned earlier that there were some limitations on what this software can do. Basically, once you get beyond a 2x2 design (e.g., 3x2), there can be some (usually minor) discrepancies between the F statistics calculated by rpsychi and the numbers that might have been returned by the ANOVA software used by the authors of the article that you are reading, if the sample sizes are unbalanced across three or more conditions; the magnitude of such discrepancies will depend on the degree of imbalance. This issue is discussed in a section starting at the bottom of page 3 of our follow-up preprint.

A further limitation is that rpsychi has trouble with very small F statistics (such as 0.02). If you have a script that makes multiple calls to f_range(), it may stop when this occurs. The only workaround I know of for this is to comment out that call (as shown in the first example above).

Here is the R code for f_range(). It is released under a CC BY license, so you can do pretty much what you like with it. I decided not to turn it into an R package because I want it to remain "quick and dirty", and packaging it would require an amount of polishing that I don't want to put in at this point. This software comes with no technical support (but I will answer polite questions if you ask them via the comments on this post) and I accept no responsibility for anything you might do with it. Proceed with caution, and make sure you understand what you are doing (for example, by having a colleague check your reasoning) before you do... well, anything in life, really.

The first thing one notices in looking at hisGoogleScholarrecord is that Dr. Guéguen is a remarkably
prolific researcher. He regularly
publishes 10 or more sole-authored empirical articles per year (this total
reached 20 in 2015), many of which include extensive fieldwork and the
collection of data from large numbers (sometimes even thousands) of
participants. Yet, none of the many research assistants and other junior
collaborators who must have been involved in these projects ever seem to be
included as co-authors, or even have their names mentioned; indeed, we have yet
to see an Acknowledgments section in any sole-authored article by Dr.
Guéguen. This seems unusual,
especially given that in some cases the data collection process must have
required the investment of heroic amounts of the confederates’ time.

It seems that some of this research is actually taken quite seriously by some psychologists. For example, it is cited
in recent work by AndrewElliot and colleagues at the University of
Rochester that claims to show that womenwearredclothesasasexualsignal (thus also providing a piece of Dr.
Guéguen’s IV/DV combination bingo card that would otherwise have been missing). The skeptical psychologist Dr. Richard Wiseman
also seems to be something of a fan of Guéguen's work; for example, in his 2009
book 59 Seconds: ThinkaLittle, ChangeaLot, Wiseman noted that "Nicolas
Guéguen has spent his career investigating some of the more unusual aspects of
everyday life, and perhaps none is more unusual than his groundbreaking work on
breasts", and he also cited Guéguen several times in his 2013 bookTheAsIfPrinciple.

But our concerns go well beyond the apparent borderlineteenagesexism that seems to characterise much of this
research. A far bigger scientific
problem is the combination of extraordinary effect sizes, remarkably high (in some cases, 100%) response rates among participants recruited in the street (cf. thisstudy, where every single one of the 500 young female
participants who were intercepted in the street agreed to reveal their age to the
researchers, and every single one of them turned out to be aged between 18 and
25), other obvious logistical obstacles, and the large number of statistical errors or mathematically impossible
results reported in many of the analyses.

We also have some concerns about the ethicality of some of Dr. Guéguen’s field
experiments. For example, in thesetwo
studies, his male confederates asked other men how likely it was that a female
confederate would have sex with them on a first date, which might be a suitable
topic for bar-room banter among friends but appears to us to be somewhat intrusive. In another study, womenparticipantsweresecretlyfilmedfrombehind with the resulting footage being shown
to male observers who rated the “sexiness” of the women’s gait (in order to
test the theory that women might walk “more sexily” in front of men when they
are ovulating; again, readers may not be totally surprised to learn that this
is what was found). In thisstudy, the debriefing procedure for the young
female participants involved handing them a card with the principal
investigator’s personal phone number; this procedure was “refined” in anotherstudy, where participants who had agreed to
give their phone number to an attractive male confederate were called back,
although it is not entirely clear by whom. (JohnSakaluk
has pointed out that there may also be issues around how these women’s
telephone numbers were recorded and stored.)

It is unclear from the studies presented that any of these protocols
received individual ethical approval, as study-specific details from an IRB are
not offered. Steps to mitigate potential harms/dangers are not mentioned, even
though in several cases data collection could have been problematic, with
confederates dressing deliberately provocatively in bars and so on. Ethical
approval is mentioned only occasionally, usually accompanied by the reference
number “CRPCC-LESTIC EA 1285”. This might look like an IRB approval code of
some kind, but in fact it is just the French national science administration’s
identification code for Dr. Guéguen’s own laboratory.

It is also noteworthy that none of the articles we have read mention any
form of funding. Sometimes, however, the expenses must have been
substantial. In thisstudy (hat tip to HarryManley
for spotting it), 99 confederates stood outside bars and administered
breathalyser tests to 1,965 customers as they left. Even though the breathalyserdevicethatwasused is a basic model that sells for €29.95, it seems that at least 21
of them were required; plus, as the “Accessories” tab of that page shows, the
standard retail price of the sterile mouthpieces (one of which was used per
participant) before they were discontinued was €4.45 per 10, meaning that the
total cash outlay for this study would have been in the region of €1500. One would have thought that a laboratory that could
afford to pay for that out of petty cash for a single study could also pick up
the tab in a nightclub from time to time.

This has been quite the saga

It is almost exactly two years to the day since we started to put
together an extensive analysis (over 15,000 words) focused on 10 sole-authored
articles by Dr. Guéguen, which we then sent to the French Psychological Society
(SFP). The SFP’s research department agreedthatwehadidentifiedanumberofissuesthatrequiredananswer
and asked Dr. Guéguen for his comments. Neither they nor we have received any
coherent response in the interim, even though it would take just a few minutes
to produce any of the following: (a) the names and contact details of any of
the confederates, (b) the field notes that were made during data collection,
(c) the e-mails that were presumably sent to coordinate the field work, (d)
administrative details such as insurance for the confederates and reimbursement
of expenses, (e) minutes of ethics committee meetings, etc.

At one point Dr. Guéguen claimed that he was too busy looking after a
sick relative to provide a response, circumstances which did not prevent him
from publishingasteadystreamoffurtherarticles in the meantime. In the autumn of 2016, he sent the SFP a
physical file (about 500 sheets of A4 paper) containing 25 reports of field
experiments that had been conducted by his undergraduates, none of which had
any relevance to the questions that we had asked. In the summer of 2017, Dr. Guéguen
finally provided the SFP with a series of half-hearted responses to our
questions, but these systematically failed to address any of the specific
issues that we had raised. For example,
in answer to our questions about funding, Dr. Guéguen seemed to suggest that
his student confederates either pay all of their out-of-pocket expenses
themselves, or otherwise regularly improvise solutions to avoid incurring those
expenses, such as by having a friend who works at each of the nightclubs that
they visit and who can get them in for free.

We want to offer our thanks here to the officials at the SFP who spent
18 months attempting to get Dr. Guéguen to accept his responsibilities as a
scientist and respond to our requests for information. They have indicated to
us that there is nothing more that they can do in their role as intermediary,
so we have decided to bring these issues to the attention of the broader
scientific community.

Hence, this post should be regarded as a reiteration of our request for
Dr. Guéguen to provide concrete answers to the questions that we have raised.
It should be very easy to provide at least some evidence to back up his
remarkable claims, and to explain how he was able to conduct such a huge volume
of research with no apparent funding, using confederates who worked for hours
or days on end with no reward, and obtain remarkable effect sizes from
generally minor social priming or related interventions, while committing so
many statistical errors and reporting so many improbable results.

Further reading

We have made a copy of the current state of our analysis of 10 articles
by Dr. Guéguen available here, along with his replies (which are
written in French). For completeness,
that folder also includes the original version of our analysis that we sent to
the SFP in late 2015, since that is the version to which Dr. Guéguen eventually
replied. The differences between the
versions are minor, but they include the removal of one or two points where we
no longer believe that our original analysis made a particularly strong case.

Despite its length (around 50 pages), we hope that interested readers
will our analysis to be a reasonably digestible introduction to the problems
with this research. There are one or two
points that we made back in December 2015 which we might not make today (either
because they are rather minor, or because we now have a better understanding of
how to report these issues now that we have more experience with the
application of tools such as GRIM and SPRITE).
Most of the original journal articles are behind paywalls, but none are
so obscure that they cannot be obtained from standard University subscriptions.